The results presented here indicate a source of heat energy was measured that is not chemical in origin.

This measurement and conclusion are in general agreement with those of Arata and Zhang [4] and Ahern[5]. Given the importance a source of high specific energy has for space technology, this work indicatesthat additional research should be pursued. If future work is better funded, calorimetry should be usedinstead of thermometry to measure the heat power.

Executive summary (for those
who want to quit now): Looks like a good
chance it’s noise.

Comments:

Breiting (‘B’ hereafter) does
the same thing the rest of the CF community does and fails to consider the
calibration constants in his cal. equations as experimental variables. He talks about doing a Propagation of Error
calc but the only variable he looks at is T explicitly. So, I did my usual, and plugged in a 1-6%
variation in cal. constants. I did it
simply by increasing and decreasing the constants in his cal equations by a
fixed percentage using the same number on all the constants. That doesn’t mean they couldn't vary
independently, I just didn’t want to bother with all that.

But to start we need to know
what the supposed error is that we are trying to explain. B also tries to do the energy per unit mass
trick, which is bogus since he doesn’t know what ‘mass’ is the right mass to
use. So backing it up, his 173 MJ/g
number works out to ~0.94W excess power signal, which he also refers to as ‘~1W’
in his exec summary.

So using the PwrC2T1Vac
equation, I calculated the power for a span of T’s, but I will only discuss the
one for 300C. His numbers give 12.94W at
300C, increase all the constants by 4% and you get 13.45W, decrease by 4% and
you get 12.42W. That’s a span of
1.03W. B only reports one calibration,
so we have no idea what the reproducibility of his calibrations is, but these
results are in the same range as the span on the Storms’ data, and on the
various reports by Miles.

But further, I had to ask why
he used a cubic equation. To get a rough
idea what might happen with a different equation, I used his equation to make a
small set of data similar in size to what he used, and then fit it with a
quadratic. At 350C. the cubic gave
17.34W and the quadratic gave 16.41W, for a difference of 0.93W. At 300C the diff was 0.88W. (Note that using the cubic gave a positive excess heat.)

In other words, simple
piddling around with the calibration equation covered the signal detected. That means to believe the calibrations, we
need a lot more info on how he chose his equations, and we need to see some
replication to assess the reproducibility of those equations.

After that we can consider
the rest of the waffling he does.

I am not going to defend
this. You do the calcs if you don’t like
what I say.

The R^2 of a quadratic fit to a known cubic’s data is not particularly useful. Instead I hand digitized the Cell 2 Vacuum (red) data from Figure 4.4 as an approximation to the real data. I then fitted it with a quartic, cubic, and a quadratic. Results are:

The R^2 values are not adequate to distinguish which model is best. The t values of the coefficients are needed (or the significance levels) so the full analytical results are needed.

The interesting thing however is the differences in the preducted power for a given temp in the upper temperature operating range. 3 sets are shown below for 300, 325, and 350C.

T

Power

model-cubic

quart

350

16.49228

0.197372

cubic

350

16.29491

quad

350

15.9999

-0.295

T

Power

Model-cubic

quart

325

14.13117

0.044798

cubic

325

14.08638

quad

325

13.98244

-0.10394

T

Power

model-cubic

quart

300

12.05278

-0.02491

cubic

300

12.07769

quad

300

12.09764

0.019952

Notice that a) the difference (model error) increases as the T increases and b) the magnitude is significantly larger that the 0.050 W claimed by Breiting for some cases. Again, Breiting needs to show more data and analysis results. Kudos to him for giving the cal. equations, because this is extremely rare in the CF field. That is what allows the above analysis.

As well, the 'sensitivity analysis' I did with the variation of 1-6% in the cal constants of the given cubic cal equation still stands as well. Proper error propagation is required...

My general conclusion still stands, the observed excess could well be noise (or a combination of noise and modelling error).

If there were an 8% shift, as Shanahan claims, much of the test shown on p. 20, the calibration runs, and the control runs would be endothermic. They would be swallowing up megajoules of heat. It would be a fantastic coincidence that the calibrations fell exactly on the zero line. This is impossible. Shanahan has a rare talent for inventing impossible physics.

If there were an 8% shift, as Shanahan claims, much of the test shown on p. 20, the calibration runs, and the control runs would be endothermic. They would be swallowing up megajoules of heat. It would be a fantastic coincidence that the calibrations fell exactly on the zero line. This is impossible. Shanahan has a rare talent for inventing impossible physics.

Readers may first notice that p.20 of the report deals with the first experiment, which is denoted a learning experience and is not used to report apparent excess heats in the report's main body. Thus it is not relevant to my discussion to date. There may well be other things going on with it. I didn't look at it since it was not used to make excess heat claims.

Further, I clearly showed that slight changes in the calibration constants have significant impacts on the predicted power computed from measured temperature. At 350C, the model changes I looked at can cause an ~200 mW error, much larger than the claimed 50 mW. Likewise at 350C, a 5% (not 8%) change induces an 820 mW error (and as noted, the global numbers imply something on the order of 944 mW). Table E1 of the report shows that between the vac and N2 cal curves there is a 574 mW difference at 300C, so the small changes in cal constants I am discussing give changes on the same order of magnitude as changing the gas space contents. This implies knowing the variation in cal constants is as important as knowing what is in the gas phase of the cell which Breiting spends considerable time discussing and compensating for.

Why Jed thinks such changes would drive the curves endothermic I don't follow. Unless he is talking about much lower temps. As one can see, at 0C the cal equations give negative powers, but that is just an indication of the fact that the real cell behavior doesn't fit the polynomial form well outside the data span, which is typical of statistical fits. And in any case, the cell is going to do what the cell does. The question is how well the equations used to interpret the data correspond to the real behavior.

Also note that a 50mW error at 12 W input is a 0.4% error. That's a better calorimeter than McKubre ever made. Do you all really believe Breiting made that good of a calorimeter on his first shot? Better error analysis is required.

I will also say at this point I looked a little bit at the chemistry used by Breiting and I find it inadequate. It is incorrect to assume the observed heat (if assumed to be real) is not at least partially explained by chemistry.

Also note that a 50mW error at 12 W input is a 0.4% error. That's a better calorimeter than McKubre ever made. Do you all really believe Breiting made that good of a calorimeter on his first shot?

Yes, I am sure he did. I expect McKubre agrees. The state of the art has improved and the people at The Aerospace Corp. are world class. (See: http://www.aerospace.org/) McKubre described his calorimeter as easy to understand but "stupid" (simple minded, rather than ultra-precise). The error in it was larger than several other calorimeters, such as Fleischmann's and Miles'.

Beiting has made a second, flow calorimeter that confirms the first one. Shanahan cannot explain this, either, except with his impossible hand-waving.

An abstract is simply a claim until substantiated with the standard types of information that would come out in the supposed subsequent paper. Thus, at this point, your claim is probably just wishful thinking.

It do look like the calormetry is very exact, as taken for granted by those who work with it, and the method used e.g. advanced interpolation using higher order polynomial which is appropriate for deterministic systems. This means that statistics is out of the window and is not a good method to apply here because the estimated variance is way to high compared to the real one due to the low degrees of freedom. In any case a figure of e.g. the relative error is xxx% would be helpful just to checkbox that non are fooled in any way. There are method that does statistics based on known variances and they could be used here in case one want to dwell on it and I think that would be the appropriate way to do it in this case. We don't have a figure

yet, good researchers know the variance of their systems and my bet is that Breiting knows quite well that all is ok. But no proof on the table for the dining party.

It do look like the calormetry is very exact, as taken for granted by those who work with it, and the method used e.g. advanced interpolation using higher order polynomial which is appropriate for deterministic systems. This means that statistics is out of the window and is not a good method to apply here because the estimated variance is way to high compared to the real one due to the low degrees of freedom. In any case a figure of e.g. the relative error is xxx% would be helpful just to checkbox that non are fooled in any way. There are method that does statistics based on known variances and they could be used here in case one want to dwell on it and I think that would be the appropriate way to do it in this case. We don't have a figure

yet, good researchers know the variance of their systems and my bet is that Breiting knows quite well that all is ok. But no proof on the table for the dining party.

Stefan, several comments...

Very exact calorimetry means very small changes can have very big impacts.

I checked the problem with low degrees of freedom. When the number of parameters (p) used in the fit approaches the number of data points (N), the use of R^2 is inappropriate and one must use what is known as the 'adjusted' R^2 = Ra^2.

Ra^2 = 1 - ( ( 1 - R^2) ( N-1 ) / ( N-p-1) )

Didn't really change the values enough to matter in the cases I looked at, but one always needs to check of course.

It is a well-known problem that linear regression can 'overfit' data sets, especially smaller ones. The chemometric procedure that is preferred is to used the PRESS value (Predictive Residual Error Sum of Squares) instead of R^2, which is determined through a process that uses jack-knifing or bootstrapping the data set to check the predictive accuracy of the statistical model. (That's where the 'P' in PRESS comes from.)

However, the requirement for determining the error in the computed output power is still the same and requires that all experimentally determined variables be included in a propagation of error calculation, which does, in the end, only give an estimate of the error. My calculations in the prior posts simply show that the 50 mW claimed error seems to be overly optimistic (which is typical in CF calorimetry) based on the fact that even in the best calorimeters the cal constants seem to have 1-5% relative standard deviations. It is always possible that Breiting has done better, but he needs to show this, not just assert it, as you indicate as well with your 'dining party' comment.

It is an observation, not a measurement. People familiar with the Corporation say this, and I think the web site backs it up. If you do not think they are world-class experts, perhaps you should tell us why. Have they made serious errors? Have their other studies been discredited?

It is an observation, not a measurement. People familiar with the Corporation say this, and I think the web site backs it up. If you do not think they are world-class experts, perhaps you should tell us why.

Well, if it is 'just' an observation with no numerical quality to it at all, then you can't claim it establishes any type of priority to the organization vs. others. I believe that in fact you are asserting that the work coming from the Aerospace Corporation is better than that from many other organizations. And my intent is to point out that that kind of 'observation' is pointless. If that method was valid, I could claim that MIT was a fly-by-night university since Hagelstein doesn't understand the difference between random and systematic. That of course would be completely incorrect about MIT. What Hagelstein does reflect primarily on Hagelstein, and only marginally on MIT. Likewise, what any Aerospace Corp. employee does reflects only marginally in a technical sense on Aerospace. Of course political and social impacts can be more prominent. So in particular, I have no idea whether the employees of Aerospace in aggregate are good, bad, or ugly, nor do I really care, because all I am interested in at the moment is Beiting. Where Beiting works is of little importance. What Beiting does is much more relevant.

Furthermore, anyone can make mistakes, so the rep of the employer has no relevance at all to the question of the quality of the specific work.

Have they made serious errors? Have their other studies been discredited?

Beiting, yes, he has. He failed to compute the error of his calibration curve properly and he failed to take into account the proper chemistry in his sample prep and subsequent experimentation. There might be more if I study the paper more, but what I've seen so far is enough to class his efforts as 'typical so-so CF community work'. And that isn't 'world-class'. With regards to other Aerospace people, no idea, don't care.

It is disappointing to read all this quibbling and fussing over claims for small amounts of excess power. If LENR reactions make energy, why hasn't someone, in 30 years since P&F, found a way to make say, ten times the current amounts, so that statistical methods are not necessary for evaluation and errors of the type Shanahan is calculating simply don't matter? Of course, JedRothwell
will say people have. But then it turns out from the papers that it was for a short time, with questionable methods of measurements, or only one time and not currently reproducible. Or worse yet, the claim is based only on an anecdote. Frustrating!